Category Archives: General Ecology

More on Old Growth Forests and Conservation

Leave a reply

This is a short blog to alert you to a well written plea for saving old growth forests in British Columbia by Karen Price. Karen works with Dave Daust and Rachel Holt, three of our ecological heroes pushing the provincial government to recognize the value of old growth forests. This problem is world-wide but the scientific data alone will not capture the general public as much as this article might.

https://northernbeat.ca/opinion/old-growth-complexity-in-a-sound-bite/

These ecologists have reported their detailed analysis in a report that you can access through the Sierra Club of BC if you want more information on the struggle here in Canada (https://sierraclub.bc.ca/laststand/ ). At present there is nothing but denial from the government and from the industry that there is a problem – the forestry industry is not overharvesting or if it is, we need the jobs. As one person told me, it is not a problem “because we plant one tree seedling for every thousand-year-old tree that we log”.

So please keep up the pressure on governments around the world. Scientists have pushed a strong agenda on sustainable logging for many years with success now looking possible because ordinary citizens demand a change, understanding that forests are more than wood. We must continue the push for sustainable forestry and old growth forest protection.

Lindenmayer, D.B., Kooyman, R.M., Taylor, C., Ward, M., and Watson, J.E.M. (2020). Recent Australian wildfires made worse by logging and associated forest management. Nature Ecology & Evolution 4, 898-900. doi: 10.1038/s41559-020-1195-5.

Price, Karen, Holt, Rachel F., and Daust, Dave (2021). Conflicting portrayals of remaining old growth: the British Columbia case. Canadian Journal of Forest Research 51, 1-11. doi: 10.1139/cjfr-2020-0453.

On Assumptions in Ecology Papers

1 Reply

What can we do as ecologists to improve the publishing standards of ecology papers? I suggest one simple but bold request. We should require at the end of every published paper a annotated list of the assumptions made in providing the analysis reported in the paper. A tabular format could be devised with columns for the assumption, the perceived support of and tests for the assumption, and references for this support or lack thereof. I can hear the screaming already, so this table could be put in the Supplementary Material which most people do not read. We could add to each paper in the final material where there are statements of who did the writing, who provided the money, and add a reference to this assumptions table in the Supplementary Material or a statement that no assumptions about anything were made to reach these conclusions.

The first response I can detect to this recommendation is that many ecologists will differ in what they state are assumptions to their analysis and conclusions. As an example, in wildlife studies, we commonly make the assumption that an individual animal having a radio collar will behave and survive just like another animal with no collar. In analyses of avian population dynamics, we might commonly assume that our visiting nests does not affect their survival probability. We make many such assumptions about random or non-random sampling. My question then is whether or not there is any value in listing these kinds of assumptions. My response is that this approach of listing what the authors think they are assuming should alert the reviewers to the elephants in the room that have not been listed.

My attention was called to this general issue by the recent paper of Ginzburg and Damuth (2022) in which they contrasted the assumptions of two general theories of functional responses of predators to prey – “prey dependence” versus “ratio dependence”. We have in ecology many such either-or discussions that never seem to end. Consider the long-standing discussion of whether populations can be regulated by factors that are “density dependent” or “density independent”, a much-debated issue that is still with us even though it was incisively analyzed many years ago.  

Experimental ecology is not exempt from assumptions, as outlined in Kimmel et al. (2021) who provide an incisive review of cause and effect in ecological experiments. Pringle and Hutchinson (2020) discuss the failure of assumptions in food web analysis and how these might be resolved with new techniques of analysis. Drake et al. (2021) consider the role of connectivity in arriving at conservation evaluations of patch dynamics, and the importance of demographic contributions to connectivity via dispersal. The key point is that, as ecology progresses, the role of assumptions must be continually questioned in relation to our conclusions about population and community dynamics in relation to conservation and landscape management.

Long ago Peters (1991) wrote an extended critique of how ecology should operate to avoid some of these issues, but his 1991 book is not easily available to students (currently available on Amazon for about $90). To encourage more discussion of these questions from the older to the more current literature, I have copied Peters Chapter 4 to the bottom of my web page at https://www.zoology.ubc.ca/~krebs/books.html for students to download if they wish to discuss these issues in more detail.

Perhaps a possible message in all this has been that ecology has always wished to be “physics-in-miniature” with grand generalizations like the laws we teach in the physical sciences. Over the last 60 years the battle in the ecology literature has been between this model of physics and the view that every population and community differ, and everything is continuing to change under the climate emergency so that we can have little general theory in ecology. There are certainly many current generalizations, but they are relatively useless for a transition from the general to the particular for the development of a predictive science. The consequence is that we now bounce from individual study to individual study, typically starting from different assumptions, with very limited predictability that is empirically testable. And the central issue for ecological science is how can we move from the present fragmentation in our knowledge to a more unified science. Perhaps starting to examine the assumptions of our current publications would be a start in this direction.  

Drake, J., Lambin, X., and Sutherland, C. (2021). The value of considering demographic contributions to connectivity: a review. Ecography 44, 1-18. doi: 10.1111/ecog.05552.

Ginzburg, L.R. and Damuth, J. (2022). The Issue Isn’t Which Model of Consumer Interference Is Right, but Which One Is Least Wrong. Frontiers in Ecology and Evolution 10, 860542. doi: 10.3389/fevo.2022.860542.

Kimmel, K., Dee, L.E., Avolio, M.L., and Ferraro, P.J. (2021). Causal assumptions and causal inference in ecological experiments. Trends in Ecology & Evolution 36, 1141-1152. doi: 10.1016/j.tree.2021.08.008.

Peters, R.H. (1991) ‘A Critique for Ecology.’ (Cambridge University Press: Cambridge, England.) ISBN:0521400171 (Chapter 4 pdf available at https://www.zoology.ubc.ca/~krebs/books.html)

Pringle, R.M. and Hutchinson, M.C. (2020). Resolving Food-Web Structure. Annual Review of Ecology, Evolution, and Systematics 51, 55-80. doi: 10.1146/annurev-ecolsys-110218-024908.

On Replication in Ecology

Leave a reply

All statistics books recommend replication in scientific studies. I suggest that this recommendation has been carried to extreme in current ecological studies. In approximately 50% of ecological papers I read in our best journals (a biased sample to be sure) the results of the study are not new and have been replicated many times in the past, often in papers not cited in ‘new’ papers. There is no harm in this happening, but it does not lead to progress in our understanding of populations, communities or ecosystems or lead to new ecological theory. We do need replication examining the major ideas in ecology, and this is good. On the other hand, we do not need more and more studies of what we might call ecological truths. An analogy would be to test in 2022 the Flat Earth Hypothesis to examine its predictions. It is time to move on.

There is an extensive literature on hypothesis testing which can be crudely summarized by “Observations of X” which can be explained by hypothesis A, B, or C each of which have unique predictions associated with them. A series of experiments are carried out to test these predictions and the most strongly supported hypothesis, call it B*, is accepted as current knowledge. Explanation B* is useful scientifically only if it leads to a new set of predictions D, E, and F which are then tested. This chain of explanation is never simple. There can be much disagreement which may mean sharpening the hypotheses following from Explanation B*. At the same time there will be some scientists who despite all the accumulated data still accept the Flat Earth Hypothesis. If you think this is nonsense, you have not been reading the news about the Covid epidemic.

Further complications arise from two streams of thought. The first is that the way forward is via simple mathematical models to represent the system. There is much literature on modelling in ecology which is most useful when it is based on good field data, but for too many ecological problems the model is believed more than the data, and the assumptions of the models are not stated or tested. If you think that models lead directly to progress, examine again the Covid modelling situation in the past 2 years. The second stream of thought that complicates ecological science is that of descriptive ecology. Many of the papers in the current literature describe a current set of data or events with no hypothesis in mind. The major offenders are the biodiversity scientists and the ‘measure everything’ scientists. The basis of this approach seems to be that all our data will be of major use in 50, 100 or whatever years, so we must collect major archives of ecological data. Biodiversity is the bandwagon of the present time, and it is a most useful endeavour to classify and categorise species. As such it leads to much natural history that is interesting and important for many non-scientists. And almost everyone would agree that we should protect biodiversity. But while biodiversity studies are a necessary background to ecological studies, they do not lead to progress in the scientific understanding of the ecosphere.

Conservation biology is closely associated with biodiversity science, but it suffers even more from the problems outlined above. Conservation is important for everyone, but the current cascade of papers in conservation biology are too often of little use. We do not need opinion pieces; we need clear thinking and concrete data to solve conservation issues. This is not easy since once a species is endangered there are typically too few of them to study properly. And like the rest of ecological science, funding is so poor that reliable data cannot be achieved, and we are left with more unvalidated indices or opinions on species changes. Climate change puts an enormous kink in any conservation recommendations, but on the other hand serves as a panchrestron, a universal explanation for every possible change that occurs in ecosystems and thus can be used to justify every research agenda, good or poor with spurious correlations.

We could advance our ecological understanding more rapidly by demanding a coherent theoretical framework for all proposed programs of research. Grace (2019) argues that plant ecology has made much progress during the last 80 years, in contrast to the less positive overview of Peters (1991) or my observations outlined above. Prosser (2020) provides a critique for microbial ecology that echoes what Peters argued in 1991. All these divergences of opinion would be worthy of a graduate seminar discussion.

If you think all my observations are nonsense, then you should read the perceptive book by Peters (1991) written 30 years ago on the state of ecological science as well as the insightful evaluation of this book by Grace (2019) and the excellent overview of these questions in Currie (2019).  I suggest that many of the issues Peters (1991) raised are with us in 2022, and his general conclusion that ecology is a weak science rather than a strong one still stands. We should celebrate the increases in ecological understanding that have been achieved, but we could advance the science more rapidly by demanding more rigor in what we publish.

Currie, D.J. (2019). Where Newton might have taken ecology. Global Ecology and Biogeography 28, 18-27. doi: 10.1111/geb.12842.

Grace, John (2019). Has ecology grown up? Plant Ecology & Diversity 12, 387-405. doi: 10.1080/17550874.2019.1638464.

Peters, R.H. (1991) ‘A Critique for Ecology.’ (Cambridge University Press: Cambridge, England.). 366 pages. ISBN: 0521400171

Prosser, J.I. (2020). Putting science back into microbial ecology: a question of approach. Philosophical Transactions of the Royal Society. Biological sciences 375, 20190240. doi: 10.1098/rstb.2019.0240.

On Feeding Birds and Other Wildlife

2 Replies

There is a very large global movement to feed birds and I want to address why this is a human success story and could be an ecological disaster. These two alternatives follow from two divergent views of the role of humans in the world’s ecosystems. The first is the dominant view that humans are the most important species on Earth, and that we can design the world to maximize our wellbeing without concern of the ecological consequences. The second is a view that we are the custodians of the Earth and that our aim must be to conserve the Earth’s biodiversity and protect its ecosystems. The second view is gaining more visibility with the conservation movement, but if it is to become dominant, there are many ecological problems that deserve our attention. One of the most obvious ones is bird feeding. There are at present no global policies on feeding birds and views on feeding are controversial (Baverstock et al. 2019).

Humans feed birds because they like to look at them and because they have a general belief that feeding in winter or severe weather prevents bird deaths (Brock et al. 2021, Clark et al. 2019). If that is correct, we would expect to see that if we had one large area where birds were fed in winter, and another in which birds were not fed, there should be a difference in population size in the two areas in the following spring. I have yet to see any study that shows this differential effect. Consider an alternative hypothesis that feeding does indeed improve bird survival in winter, but this merely feeds more predators that now have a larger prey base, so the improvement is largely in the predator populations.  It is certainly true for some migratory bird species that if they are fed they can overwinter in more northerly areas or in cities and towns, so geographic winter ranges can expand.

Perhaps the most obvious impact of feeding birds and providing water is the transmission of diseases associated with feeding stations and bird baths. Lawson et al. (2017) explored this problem with bird feeding in Great Britain and found emerging diseases over a 25-year period, focusing on protozoan, viral, and bacterial diseases with contrasting modes of transmission. They also considered mycotoxin contamination of food residues in bird feeders, which present a direct risk to bird health. Rogers et al. (2018) described a mortality event in a declining population of band-tailed pigeons in California with a loss off about 18,000 pigeons associated with tricomonosis in a drought in which birds visited artificial water sites like bird baths. Purple et al. (2015) have demonstrated that the protozoan parasite Trichomonas gallinae could persist in bird baths.

There is a certain irony in the general belief that feeding improves the survival of wild birds. I am reminded of an old story about the English ornithologist David Lack who in the 1930s was talking to a local bird club about his long-term study for a life table of the English Robin. He reported from his banding studies that the life expectancy of the robin was about one year. After his talk, an elderly woman came up to him and started beating him over the head with her umbrella. Once she calmed down, she challenged him because she had a robin singing in her back yard for the last 10 years, so she assumed it was the same robin.

There are other consequences of feeding birds. One is the attraction of squirrels to bird feeders, and the subsequent displacement of birds. One study in southern England showed that grey squirrels occupied the feeders nearly half of the time they were in service (Hanmer et al. 2018). Another consequence of feeders is feed spilled to the ground which can attract rats and other less desirable species in urban settings. Many of these problems are not unique to bird feeding. Fležar et al. (2019) used cameras to investigate sites where European brown bears were being artificially fed year-round on plant-food and carrion from road kills in Slovenia. Over one year they detected 23 vertebrate species at the feeding sites in about 68,000 photos, most frequently brown bears, red foxes and European badgers, but also about half of the species coming to the feeding sites were birds. Roe deer also used these bear feeding sites, even though it is technically illegal to feed roe deer in this jurisdiction because deer feeding on corn and other plants materials can lead to fatal metabolic diseases. The key point is that feeding stations can attract a variety of non-target species with largely unknown consequences for the local wildlife community.  

It will take a brave set of ecologists and veterinarians to define and test the critical hypotheses that arise from feeding wildlife of any kind if only because of the vested interests of the bird seed producers along with so many humans who ‘know’ that feeding is ‘good’ for wildlife. The irony of all this in the end is that many people in parts of the Earth suffer from poor nutrition and starvation while in the first world we use agricultural products to feed birds and other wildlife.

Baverstock, S., Weston, M.A., and Miller, K.K. (2019). A global paucity of wild bird feeding policy. Science of The Total Environment 653, 105-111. doi: 10.1016/j.scitotenv.2018.10.338.

Brock, M., Doremus, J., and Li, Liqing (2021). Birds of a feather lockdown together: Mutual bird-human benefits during a global pandemic. Ecological Economics 189, 107174. doi: 10.1016/j.ecolecon.2021.107174.

Clark, D.N., Jones, D.N., and Reynolds, S.J. (2019). Exploring the motivations for garden bird feeding in south-east England. Ecology and Society 24, 26. doi: 10.5751/ES-10814-240126.

Fležar, Urša, Costa, B., and Krofel, M. (2019). Free food for everyone: artificial feeding of brown bears provides food for many non-target species. European Journal of Wildlife Research 65, 1. doi: 10.1007/s10344-018-1237-3.

Hanmer, H.J., Thomas, R.L., and Fellowes, M.D.E. (2018). Introduced Grey Squirrels subvert supplementary feeding of suburban wild birds. Landscape and Urban Planning 177, 10-18. doi: 10.1016/j.landurbplan.2018.04.004.

Lawson, B., Robinson, R. A., and Cunningham, A. A. (2018). Health hazards to wild birds and risk factors associated with anthropogenic food provisioning. Philosophical Transactions of the Royal Society, Biological Sciences 373 (1745): 20170091. doi: 10.1098/rstb.2017.0091.

Purple, K.E. and Gerhold, R.W. (2015). Persistence of two isolates of Trichomonas gallinae in simulated bird baths with and without organic material. Avian Diseases 59, 472-474. doi: 10.1637/11089-041115-Reg.1.

Rogers, K.H., Girard, Y.A., Woods, L.W., and Johnson, C.K. (2018). Avian trichomonosis mortality events in band-tailed pigeons (Patagioenas fasciata) in California during winter 2014–2015. International Journal for Parasitology: Parasites and Wildlife 7, 261-267. doi: 10.1016/j.ijppaw.2018.06.006.

On the Canadian Biodiversity Observation Network (CAN BON)

Leave a reply

I have been reading the report of an exploratory workshop from July 2021 on designing a biodiversity monitoring network across Canada to address priority monitoring gaps and engage Indigenous people across Canada. The 34 pages of their workshop report can be accessed here, and I recommend you might read it before reading my comments on the report:

https://www.nserc-crsng.gc.ca/Media-Media/NewsDetail-DetailNouvelles_eng.asp?ID=1310

I have a few comments on this report that are my opinion only. I think the Report on this workshop outlines a plan so grand and misguided that it could not be achieved in this century, even with a military budget. The report is a statement of wisdom put together with platitudes. Why is this and what are the details that I believe to be unachievable?

The major goal of the proposed network is to bring together everyone to improve biodiversity monitoring and address the highest priority gaps to support biodiversity conservation. I think most of the people of Canada would support these objectives, but what does it mean? Let us do a thought experiment. Suppose at this instant in time we knew the distribution and the exact abundance of every species in Canada. What would we know, what could we manage, what good would all these data be except as a list taking up terabytes of data? If we had these data for several years and the numbers or biomass were changing, what could we do? Is all well in our ecosystems or not? What are we trying to maximize when we have no idea of the mechanisms of change? Contrast these concerns about biodiversity with the energy and resources applied in medicine to the mortality of humans infected with Covid viruses in the last 3 years. A monumental effort to examine the mechanisms of infection and ways of preventing illness, with a clear goal and clear measures of progress toward that goal.

There is no difficulty in putting out “dream” reports, and biologists as well as physicists and astronomers, and social scientists have been doing this for years. But in my opinion this report is a dream too far and I give you a few reasons why.

First, we have no clear definition of biodiversity except that it includes everything living, so if we are going to monitor biodiversity what exactly should we do? For some of us monitoring caribou and wolves would be a sufficient program, or whales in the arctic, or plant species in peat bogs. So, to begin with we have to say what operationally we would define as the biodiversity we wish to monitor. We could put all our energy into a single group of species like birds and claim that these are the signal species to monitor for ecosystem integrity. Or should we consider only the COSEWIC list of Threatened or Endangered Species in Canada as our major monitoring concern? So, the first job of CAN BON must be to make a list of what the observation network is supposed to observe (Lindenmayer 2018). There is absolutely no agreement on that simple question within Canada now, and without it we cannot move forward to make an effective network.

The second issue that I take with the existing report is that the emphasis is on observations, and then the question is what problems will be solved by observation alone. The advance of ecological science has been based on observation and experiment directed to specific questions either of ecological interest or of economic interest. In the Pacific salmon fishery for example the objective of observation is to predict escapement and thus allowable harvest quotas. Despite years of high-quality observations and experiments, we are still a long way from understanding the ecosystem dynamics that drive Pacific salmon reproduction and survival.

Contrast the salmon problem with the caribou problem. We have a reasonably good understanding of why caribou populations are declining or not, based on many studies of predator-prey dynamics, harvesting, and habitat management. At present the southern populations of caribou are disappearing because of a loss of habitat because of land use for forestry and mining, and the interacting nexus of factors is well understood. What we do not do as a society is put these ideas into practice for conservation; for example, forestry must have priority over land use for economic reasons and the caribou populations at risk suffer. Once ecological knowledge is well defined, it does not lead automatically to action that biodiversity scientists would like. Climate change is the elephant in the room for many of our ecological problems but it is simultaneously easy to blame and yet uneven in its effects.

The third problem is funding, and this overwhelms the objectives of the Network. Ecological funding in general in Canada is a disgrace, yet we achieve much with little money. If this ever changes it will require major public input and changed governmental objectives, neither is under our immediate control. One way to press this objective forward is to produce a list of the most serious biodiversity problems facing Canada now along with suggestions for their resolution. There is no simple way to develop this list. A by-product of the current funding system in Canada is the shelling out of peanuts in funding to a wide range of investigators whose main job becomes how to jockey for the limited funds by overpromising results. Coordination is rare partly because funding is low. So (for example) I can work only on the tree ecology of the boreal forest because I am not able to expand my studies to include the shrubs, the ground vegetation, the herbivores, and the insect pests, not to mention the moose and the caribou.  

For these reasons and many more that could be addressed from the CAN BON report, I would suggest that to proceed further here is a plan:

  1. Make a list of the 10 or 15 most important questions for biodiversity science in Canada. This alone would be a major achievement.
  2. Establish subgroups organized around each of these questions who can then self-organize to discuss plans for observations and experiments designed to answer the question. Vague objectives are not sufficient. An established measure of progress is essential.
  3. Request a realistic budget and a time frame for achieving these goals from each group.  Find out what the physicists, astronomers, and medical programs deem to be suitable budgets for achieving their goals.
  4. Organize a second CAN BON conference of a small number of scientists to discuss these specific proposals. Any subgroup can participate at this level, but some decisions must be made for the overall objectives of biodiversity conservation in Canada.

These general ideas are not particularly new (Likens 1989, Lindenmayer et al. 2018). They have evolved from the setting up of the LTER Program in the USA (Hobbie 2003), and they are standard operating procedures for astronomers who need to come together with big ideas asking for big money. None of this will be easy to achieve for biodiversity conservation because it requires the wisdom of Solomon and the determination of Vladimir Putin.

Hobbie, J.E., Carpenter, S.R., Grimm, N.B., Gosz, J.R., and Seastedt, T.R. (2003). The US Long Term Ecological Research Program. BioScience 53, 21-32. doi: 10.1016/j.oneear.2021.12.008

Likens, G. E. (Ed.) (1989). ‘Long-term Studies in Ecology: Approaches and Alternatives.’ (Springer Verlag: New York.) ISBN: 0387967435

Lindenmayer, D. (2018). Why is long-term ecological research and monitoring so hard to do? (And what can be done about it). Australian Zoologist 39, 576-580. doi: 10.7882/az.2017.018.

Lindenmayer, D.B., Likens, G.E., and Franklin, J.F. (2018). Earth Observation Networks (EONs): Finding the Right Balance. Trends in Ecology & Evolution 33, 1-3. doi: 10.1016/j.tree.2017.10.008.

On Global Science and Local Science

Leave a reply

I suggest that the field of ecology is fragmenting into two large visions of the science which for the sake of simplicity I will call Global Science and Local Science. This fragmentation is not entirely new, and some history might be in order.

Local Science deals with local problems, and while it aspires to develop conclusions that apply to a broader area than the small study area, it has always been tied to useful answers for practical questions. Are predators the major control of caribou declines in northern Canada? Can rats on islands reduce ground-nesting birds to extinction? Does phosphate limit primary production in temperate lakes? Historically Local Science has arisen from the practical problems of pest control and wildlife and fisheries management with a strong focus on understanding how populations and communities work and how humans might solve the ecological problems they have largely produced (Kingsland 2005). The focus of Local Science was always on a set of few species that were key to the problem being studied. As more and more wisdom accumulated on local problems, ecologists turned to broadening the scope of enquiry, asking for example if solutions discovered in Minnesota might also be useful in England or vice versa. Consequently, Local Science began to be amalgamated into a broader program of Global Science.

Global Science can be defined in several ways. One is purely financial and big dollars; this not what I will discuss here. I want to discuss Global Science in terms of ecological syntheses, and Global Science papers can often be recognized by having dozens to hundreds of authors, all with data to share, and with meta-analysis as the major tool of analysis. Global Science is now in my opinion moving away from the experimental approach that was a triumph of Local Science. The prelude to Global Science was the International Biological Program (IBP) of the 1970s that attempted to produce large-scale systems analyses of communities and ecosystems but had little effect in convincing many ecologists that this was the way to the future. At the time the problem was largely the development of a theory of stability, a property barely visible in most ecological systems.

Global Science depends on describing patterns that occur across large spatial scales. These patterns can be discovered only by having an extensive, reliable set of local studies and this leads to two problems. The first is that there may be too few reliable local studies. This may occur because different ecologists use different methods of measurement, do not use a statistically reliable sampling design, or may be constrained by a lack of funding or time. The second problem is that different areas may show different patterns of the variables under measurement or have confounding causes that are not recognized. The approach through meta-analysis is fraught with the decisions that must be made to include or exclude specific studies. For example, a recent meta-analysis of the global insect decline surveyed 5100 papers and used 166 of them for analysis (van Klink et al. 2020). It is not that the strengths and limitations of meta-analysis have been missed (Gurevitch et al. 2018) but rather the question of whether they are increasing our understanding of the Earth’s ecology. Meta-analyses can be useful in suggesting patterns that require more detailed analyses. In effect they violate many of the rules of conventional science in not having an experimental design, so that they suggest patterns but can be validated only by a repeat of the observations. So, in the best situations meta-analyses lead us back to Local Science. In some situations, meta-analyses lead to no clear understanding at all, as illustrated in the conclusions of Geary et al. (2020) who investigated the response of terrestrial vertebrate predators to fire:

“There were no clear, general responses of predators to fire, nor relationships with geographic area, biome or life-history traits (e.g. body mass, hunting strategy and diet). Responses varied considerably between species.” (page 955)

Note that this study is informative in that it indicates that ecologists have not yet identified the variables that determine the response of predators to fire. In other cases, meta-analysis has been useful in redirecting ecological questions because the current global model does not fit the facts very well (Szuwalski et al. 2015).

The result of this movement within both ecological and conservation science toward Global Science has been a shift in the amount of field work being done. Rios-Saldana et al. (2018) surveyed the conservation literature over the last 35 years and found that fieldwork-based publications decreased by 20% in comparison to a rise of 600% and 800% in modelling and data analysis studies. This conclusion could be interpreted that ecologists now realize that less fieldwork is needed at this time, or perhaps the opposite. 

In an overview of ecological science David Currie (2019) described an approach to understanding how progress in ecology has differed from that in the physical sciences. He suggests that the physical sciences focused on a set of properties of nature whose variation they analyzed. They developed ‘laws’ Like Newton’s laws or motion that could be tested in simple or complex systems. By contrast ecology has developed largely by asking how processes like competition or predation work, and not by asking questions about the properties of natural systems, which is what interests the general public trying to solve problems in conservation or pest or fisheries management. Currie (2019) summarized his approach as follows:

“Successful disciplines identify specific goals and measure progress toward those goals. Predictive accuracy of properties of nature is a measure of that progress in ecology. Predictive accuracy is the objective evidence of understanding. It is the most useful tool that science can offer society.” (page 18)

Many of these same questions underlay the critical appraisal of ecology by Peters (1991).

There is no one approach to ecological science, but we need to continue to ask what progress is being made with every approach. These are key questions for the future of ecological research, and they are worthy of much more discussion because they determine what students will be taught and what kinds of research will be favoured for funding in the future.

Currie, D.J. (2019). Where Newton might have taken ecology. Global Ecology and Biogeography 28, 18-27. doi: 10.1111/geb.12842.

Geary, W.L., Doherty, T.S., Nimmo, D.G., Tulloch, A.I.T., and Ritchie, E.G. (2020). Predator responses to fire: A global systematic review and meta-analysis. Journal of Animal Ecology 89, 955-971. doi: 10.1111/1365-2656.13153.

Gurevitch, J., Koricheva, J., Nakagawa, S., and Stewart, G. (2018). Meta-analysis and the science of research synthesis. Nature 555, 175-182. doi: 10.1038/nature25753.

Kingsland, Sharon .E. (2005) ‘The Evolution of American Ecology, 1890-2000  ‘ (Johns Hopkins University Press: Baltimore.) ISBN: 0801881714

Peters, R.H. (1991) ‘A Critique for Ecology.’ (Cambridge University Press: Cambridge, England.) ISBN: 0521400171

Ríos-Saldaña, C. Antonio, Delibes-Mateos, Miguel, and Ferreira, Catarina C. (2018). Are fieldwork studies being relegated to second place in conservation science? Global Ecology and Conservation 14: e00389. doi: 10.1016/j.gecco.2018.e00389.

Szuwalski, C.S., Vert-Pre, K.A., Punt, A.E., Branch, T.A., and Hilborn, R. (2015). Examining common assumptions about recruitment: a meta-analysis of recruitment dynamics for worldwide marine fisheries. Fish and Fisheries 16, 633-648. doi: 10.1111/faf.12083.

van Klink, R., Bowler, D.E., Gongalsky, K.B., Swengel, A.B., Gentile, A. and Chase, J.M. (2020). Meta-analysis reveals declines in terrestrial but increases in freshwater insect abundances. Science 368, 417-420. doi: 10.1126/science.aax9931.

On Cats and Birds and Policy Gaps

1 Reply

Many people in western societies like to keep cats as pets, and with that simple observation we run into two problems that require resolution. First, cats are killers of wildlife, particularly birds but also an array of other small prey. Most people do not believe this, because cats are adored and make good, if somewhat disinterested pets. So, my first point might be that if you think cats are not killers, I invite you to keep another cat like a mountain lion for a pet. But we need some data on the kill rate of cats. Before we begin this search, we should note that cats can be kept inside dwellings or in cat runs with no access to birds or other prey. If this is the case, no problem exists for wildlife, and you can skip to the bottom of this blog for one other issue to recognize.

How much mortality can be traced to cats roaming out of doors? This will include normal house cats let out to roam at night, as well as wild cats that have been discarded by their owners into the wild. There is extensive literature on cats killing birds. If you want a brief introduction Greenwall et al. (2019) discuss a nesting colony of Fairy Terns, a threatened species of Australian seabird, along a beach in southwestern Australia. With detailed observations and photographic data, they recorded the complete failure of all 111 nests in this colony with the loss of all tern chicks in the early summer of 2018. The predator was a single desexed feral cat. Many local governments allow the capture of feral cats with the protocol that they are desexed and then released back into the environment. Clearly desexing and release does not remove the problem.

The domestic cat has been spread world-wide, so that the cat problem is not a local one. Li et al. (2021) completed a survey of feral cat kill rates in the eastern part of China and found that the minimum annual loss of wildlife to feral cats was in the range of 2.7-5.5 billion birds, and 3.6-9.8 billion mammals, as well as large numbers of amphibians, reptiles, and fish. In gardens in Western Europe cat predation on ringed birds studied with precise data showed that up to 25% of dead birds were killed by cats, but these data varied greatly among species (Pavisse et al. 2019). For the European Robin which often feeds on the ground 40% of all ringed birds were killed by cats, for the European Greenfinch the figure was 56% of ringed birds killed. These are just two examples of an extensive literature on cat kills going back many years (Calvert et al. 2013).

What can we do about this predation? As with too many conservation issues the answer is simple but difficult to implement: Ban all cats from free-ranging unless they are on a leash and under control. Keep cats in the house or in special cat runs that are confined outdoors. Ban completely stupid programs of catching feral cats, sterilizing them, and releasing them back to the wild to continue their killing. Cats may make marvellous pets but need to be kept indoors. Many people would support these measures but many cat owners would disagree about such measures. Some progress is being made in urban environments in which some suburbs do not permit cats to roam freely.

Feral cats are a serious issue in Australia because they attack many threatened birds and reptiles (Doherty et al. 2019). In this case a federal environmental policy to kill 2 million cats is popular but from a conservation viewpoint still a poor policy. We do not know if killing 2 million cats is too much or too few, and without specific goals for conservation and careful monitoring of bird populations widespread killing my not achieve the goal of protection for threatened species. Eradications of cats on islands is often feasible, but no mainland eradication is currently possible.

As conservation biologists know too well, when humans are the problem, wise policies may not be implemented. So, the second issue and the bottom line might be to consider the human costs of cat ownership. Adhikari et al. (2020) report a highly significant association between the risk of dying from colon cancer and cat ownership. These results are not confounded by sedentary lifestyle, cigarette smoking or socio-economic status. In a similar study Adhikari et al. (2019) found that living with a cat significantly increased the death rate from lung cancer among women. The cause of these associations cannot yet be deciphered but are postulated to result from mycotoxins, toxic secondary metabolites produced by fungi (moulds) in cereal crops used in cat food. Aflatoxin is a mycotoxin that produces well-known chemicals that are seriously toxic to animals and humans.

These kinds of studies of associations arising from surveys can be tossed off by the typical comments ‘these-things-do-not-concern-my cats’ or ‘that there is no proof of the exact cause’ so if you are concerned you might investigate the literature on both mycotoxins and the diseases that cats carry.

It is up to humans to solve human problems, but up to conservation biologists to point out the detrimental effects of household pets and their feral cousins on wildlife. The present situation is a complete policy failure by governments at all levels. Good science is relatively easy, good policy is very difficult.

Adhikari, Atin, Adhikari, A., Jacob, N. K., and Zhang, J. (2019). Pet ownership and the risk of dying from lung cancer, findings from an 18 year follow-up of a US national cohort. Environmental Research 173, 379-386. doi: 10.1016/j.envres.2019.01.037.

Adhikari, Atin, Adhikari, A., Wei, Y. D., and Zhang, J. (2020). Association between pet ownership and the risk of dying from colorectal cancer: an 18-year follow-up of a national cohort. Journal of Public Health 28, 555-562. doi: 10.1007/s10389-019-01069-1.

Calvert, A.M., Bishop, C.A., Elliot, R.D., Krebs, E.A., Kydd, T.M., Machtans, C.S., Robertson, G.J., 2013. A synthesis of human-related avian mortality in Canada. Avian Conservation and Ecology 8: 11. doi 10.5751/ACE-00581-080211.

Doherty, T.S., Driscoll, D.A., Nimmo, D.G., Ritchie, E.G., and Spencer, R. (2019). Conservation or politics? Australia’s target to kill 2 million cats. Conservation Letters 12, e12633. doi: 10.1111/conl.12633.

Li, Yuhang, Wan, Yue, Shen, Hua, Loss, S.R., Marra, P.P., and Li, Zhongqiu (2021). Estimates of wildlife killed by free-ranging cats in China. Biological Conservation 253, 108929. doi: 10.1016/j.biocon.2020.108929.

Greenwell, C.N., Calver, M.C., and Loneragan, N.R. (2019). Cat Gets Its Tern: A Case Study of Predation on a Threatened Coastal Seabird. Animals 9, 445. doi: 10.3390/ani9070445.

Pavisse, R., Vangeluwe, D., and Clergeau, P. (2019). Domestic Cat Predation on Garden Birds: An Analysis from European Ringing Programmes. Ardea 107, 103-109. doi: 10.5253/arde.v107i1.a6.

Ecology for Now or the Future

Leave a reply

With the general belief that the climate is changing and that these changes must continue for at least 100 years due to the atmospheric physics of greenhouse gases, ecologists of all stripes face a difficult decision. The optimist says to continue with current studies, with due analysis of data from the past getting published, with the assumption that the future will be like the past. We know that the future will not be like the past so our belief in the future is a projection not a prediction. Does this mean that ecologists today should really be in the History Department of the Faculty of Arts?

Well, no one would allow this to happen, since we are scientists not the connivers of untestable stories of past events that masquerade as history, a caricature of the scientific method. The general problem is applicable to all the sciences. The physical sciences of physics and chemistry are fixed for all eternity, so physicists do not have to worry. The geological sciences are a mix of history and applied physics with hypotheses that are partly testable in the current time but with an overall view of future predictions that have a time scale of hundreds to thousands of years. One way to look at this problem is to imagine what a textbook of Physics would look like in 100 years, compared to a textbook of Geology or Biology or Ecology.

Ecological science is burdened by the assumption of equilibrium systems which we all know to be false since we have the long-term evidence of evolution staring at us as well as the short-term evidence of climate change. Ecologists have only two options under these constraints: assume equilibrium conditions over short time-frames or model the system to provide future projections of change. First, assume we are dealing with equilibrium systems within a defined time frame so that we can define clear hypotheses and test them on a short time scale of 10 to perhaps 20 years so we reach a 10–20-year time scale understanding of ecological processes. This is how most of our ecological work is currently carried out. If we wish to study the pollination of a particular set of plants or a crop, we work now to find out which species pollinate, and then hopefully in a short time frame try to monitor if these species are increasing or declining over our 10–20-year time span. But we do this research with the knowledge that the time frame of our ecological information is at most 100 years and mostly much less. So, we panic with bird declines over a 48 year time span (Rosenberg et al. 2019) with an analysis based on unreliable population data, and we fail to ask what the pattern might look like if we had data for the last 100 years or what it might look like in the next 100 years. We have the same problem with insect declines (Wagner et al. 2021, Warren et al. 2021).

If we wish to improve these studies we need much better monitoring programs, and with some notable exceptions there is little sign yet that this is happening (Lindenmayer et al. 2018, 2020). But the real question must come back to the time frame and how we can make future projections. We cannot do this with a 3-year funding cycle. If most of our conservation problems can be traced to human alterations of the biosphere then we must document these carefully with the usual scientific methods. At present I would hazard a guess that 95% of all endangered species are due directly to human meddling, even if we remove the effect of climate change.  

One way to make future projections is to model the population or community under study. A great deal of modelling is being done and has been done but there is little follow-through of how accurate the model predictions have been and little plan to test these projections. We may be successful with models that predict next year’s population or community dynamics, given much background data but that is only a tiny step to estimating what will be there in even 20 or 30 years. We need testable models more than panic calls about declining species with no efforts to discover if and why.

Where does that leave us? We must continue to analyse the ecological state of our current populations and communities and beware of the assumption that they are equilibrium systems. While physics for the future is rather well settled, ecological questions are not.

Lindenmayer, D.B., Likens, G.E., and Franklin, J.F. (2018). Earth Observation Networks (EONs): Finding the Right Balance. Trends in Ecology & Evolution 33, 1-3. doi: 10.1016/j.tree.2017.10.008.

Lindenmayer, D.B., Kooyman, R.M., Taylor, C., Ward, M., and Watson, J.E.M. (2020). Recent Australian wildfires made worse by logging and associated forest management. Nature Ecology & Evolution 4, 898-900. doi: 10.1038/s41559-020-1195-5.

Rosenberg, K.V., et al. (2019). Decline of the North American avifauna. Science 366, 120-124. doi: 10.1126/science.aaw1313.

Wagner, D.L., Grames, E.M., Forister, M.L., Berenbaum, M.R., and Stopak, D. (2021). Insect decline in the Anthropocene: Death by a thousand cuts. Proceedings of the National Academy of Sciences 118, e2023989118. doi: 10.1073/pnas.2023989118.

Warren, M.S., et al. (2021). The decline of butterflies in Europe: Problems, significance, and possible solutions. Proceedings of the National Academy of Sciences 118 (2), e2002551117. doi: 10.1073/pnas.2002551117.

On Biodiversity Science

Leave a reply

With David Attenborough and all the amazing picture books on biodiversity there can be few people in the world who have not been alerted to the array of beautiful and interesting species on Earth. Until recently the subject of biodiversity, known to First Nations since long, long ago, had not entered the western world of automobiles, industry, farming, fishing, music, theatres, and movies. Biodiversity is now greatly appreciated by most people, but perhaps more as entertainment for western societies and more for subsistence food in less wealthy parts of our world.

There are many different measures of ‘biodiversity’ and when discussing how we should protect biodiversity we should be careful about exactly how this word is being used. The number of different species in an area is one simple measure of biodiversity. But often the types of organisms being considered are less well defined. Forest ecologists attempt to protect forest biodiversity, but logging companies are more concerned only with trees and tree size for commercial use. Bird watchers are concerned with birds and have developed much citizen science in counting birds. Mushroom connoisseurs may worry about what edible mushrooms will be available this summer. But in many cases biodiversity scientists recognize that the community of organisms and the ecosystem that contains them would be a more appropriate unit of analysis. But as the number of species in an ecosystem increases, the complexity of the ecosystem becomes unmanageable. A single ecosystem may have hundreds to thousands of species, and we are in the infant stage of trying to determine how to study these biological systems.

One result is that, given that there are perhaps 10 million species on Earth and only perhaps 10,000 biologists who study biodiversity, where do we begin? The first and most popular way to answer this question is to pick a single species and concentrate on understanding its ecology. This makes are researcher’s life fairly simple. If elephants in Africa are under threat, find out all about the ecology of elephants. If a particular butterfly in England is very rare, try to find out why and how to protect them. This kind of research is very valuable for conservation because it provides a detailed background for understanding the requirements of each species. But the single species approaches lead into at least two quagmires. First, all species exist in a web of other species and understanding this web greatly expands the problem. It is possible in many cases to decipher the effects other species have on our elephants or butterflies, but this requires many more scientists to assist in analysing the species’ food chain, its diseases, its predators and parasites, and that is only a start. The second quagmire is that one of the general rules of ecology is that most species on Earth are rare, and few are common. So that we must concentrate our person-power on the common species because they are easier to find and study. But it is often the rare species that are of conservation concern, and so we should focus on them rather than the common species. In particular, given that only about 10% of the species on Earth have been described scientifically, we may often be assigned a species that does not have any information on its food habits or habitat requirements, its distribution, and how its abundance might be changing over time, a lifetime research program.

The result of this general overview is that the mantra of our day – Protect Biodiversity – begins as a compelling slogan and ends in enormous scientific complexity. As such it falls into the category of slogans like ‘Reduce Poverty’ and ‘Peace on Earth’, something we can all agree on, but the devil is in the details of how to achieve that particular goal.

One way to avoid all these pitfalls has been to jump over the problems of individual species and analyse communities of species or entire ecosystems. The result of this approach is to boil down all the species in the community to a number that estimates “biodiversity” and then use that number in relating ‘biodiversity’ to community attributes like ‘productivity’ or ‘stability’. This approach leads to testing hypotheses like ‘Higher biodiversity leads to greater stability’. There are serious problems with this approach if it is used to test any such hypothesis. First, biodiversity in this example must be rigorously defined as well as stability. The fact that higher biodiversity of butterflies in a particular region is associated with a more stable abundance of these butterflies over time is worthy of note but not of generalization to global communities or ecosystems. And as in all ecological studies we do not know if this is a generalization applicable to all butterfly populations everywhere until many more studies have been done.

A second problem is that this community or ecosystem approach to address ecological questions about biodiversity is not very useful in promoting conservation which boils down to particular species in particular environments. It should force us back to looking at the population ecology of species that are of conservation concern. It is population ecologists who must push forward the main goals of the conservation of the Earth’s biota, as Caughley (1994) recognized long ago.

The practical goals of conservation have always been local, and this constraint is mostly ignored in papers that demand some global research priorities and global ecological rules. The broad problem is that the conservation of biodiversity is a gigantic scientific and political problem that is currently underfunded and in its scientific infancy. At the present too much biodiversity research is short-term and not structured in a comprehensive framework that identifies critical problems and concentrates research efforts on these problems (Nichols et al. 2019, Sutherland et al. 2018). One more important issue for a seminar discussion group. 

Caughley, G. (1994). Directions in conservation biology. Journal of Animal Ecology 63, 215-244. doi: 10.2307/5542

Nichols, J.D., Kendall, W.L., and Boomer, G.S. (2019). Accumulating evidence in ecology: Once is not enough. Ecology and Evolution 9, 13991-14004. doi: 10.1002/ece3.5836.

Sutherland, W.J., Butchart, Stuart H.M., Connor, B., Culshaw, C., Dicks, L.V., et al. (2018). A 2018 Horizon Scan of Emerging Issues for Global Conservation and Biological Diversity. Trends in Ecology & Evolution 33, 47-58. doi: 10.1016/j.tree.2017.11.006.

Ecological Science: Monitoring vs. Stamp Collecting

Leave a reply

Ecology as a science is deeply divided by two views of the natural world. First is the view that we need to monitor changes in the distribution and abundance of the biota and try to explain why these changes are occurring through experiments. The second view is that we need to understand ecosystems as complex systems, and this can be done only by models with a tenuous link to data. It is worth discussing the strengths and weaknesses of each of these views of our science.

The first view could be described as the here-and-now approach, studies of how the populations, communities, and ecosystems are changing in all the biomes on Earth. It is clearly impossible to do this properly because of a lack of funding and person-power. Because of this impossibility we change our focus to short-term studies of populations, species, or communities and try to grasp what is happening in the time scale of our lifetime. This had led to a literature of confusing short-term studies of problems that are long-term. Experiments must be short term because of funding. Any long-term studies such of those highlighted in textbooks are woefully inadequate to support the conclusions reached. Why is this? It is the baffling complexity of even the simplest ecological community. The number of species involved is too large to study all of them, so we concentrate on the more abundant species, assuming all the rare species are of little consequence. This has led to a further division within the monitoring community between conservation ecologists who worry about the extinction of larger, dominant species and those that worry about the loss of rare species.

The first approach is further compromised by climate change and human exploitation of the Earth. You could invest in the study of a grassland ecosystem for 15 years only to find it turned into a subdivision of houses in year 16. We try to draw conclusions in this hypothetical case by the data of the 15 years of study. But if physiological ecologists and climate change models are even approximately correct, the structure of similar grassland ecosystems will change due to rainfall and temperature shifts associated with greenhouse gases. Our only recourse is to hope that evolution of physiological tolerances will change fast enough to rescue our species of interest. But there is no way to know this without further empirical studies that monitor climate and the details of physiological ecology. And we talk now about understanding only single species and are back to the complexity problem of species interactions in communities.

The second approach is to leap over all this complexity as stamp-collecting and concentrate on the larger issues. Are our ecological communities resilient to climate change and species invasions? Part of this approach comes from paleoecology and questions of what has happened during the last 10,000 or one million years. But the details that emerge from paleoecology are very large scale, very interesting but perhaps not a good guide to our future under climate change. If a forward-looking forestry company wishes to make sure it has 100-year-old trees to harvest in 100 years’ time, what species should they plant now in central Canada? Or if a desert community in Chile is to be protected in a national park, what should the management plan involve? These kinds of questions are much harder to answer than simpler ones like how many dingoes will we have in central Australia next year.

Long-term experiments could bridge the gap between these two approaches to ecological understanding, but this would mean proper funding and person-power support for numerous experiments that would have a lifetime of 25 to 100 years or more. This will never happen until we recognize that the Earth is more important than our GDP, and that economics is the king of the sciences.

Where does all this lead ecological scientists? Both approaches have been important to pursue in what has been the first 100 years of ecological studies and they will continue to be important as our ecological understanding improves. We need good experimental science on a small scale and good broad thinking on long time scales with extensive studies of everything from coral reefs to the Alaskan tundra. We need to make use of the insights of behavioural ecology and physiological ecology in reaching our tentative conclusions. And if anyone tells you what will happen in your lifetime in all our forests and all the biodiversity on Earth, you should be very careful to ask for strong evidence before you commit to a future scenario.

Beller, E.E., McClenachan, L., Zavaleta, E.S., and Larsen, L.G. (2020). Past forward: Recommendations from historical ecology for ecosystem management. Global Ecology and Conservation 21, e00836. doi: 10.1016/j.gecco.2019.e00836.

Bro-Jørgensen, J., Franks, D.W., and Meise, K. (2019). Linking behaviour to dynamics of populations and communities: application of novel approaches in behavioural ecology to conservation. Philosophical Transactions of the Royal Society, B.  Biological Sciences 374: 20190008.  doi: 10.1098/rstb.2019.0008.

Lidicker, W.Z. (2020). A Scientist’s Warning to humanity on human population growth. Global Ecology and Conservation 24, e01232. doi: 10.1016/j.gecco.2020.e01232.

McGowan, D. W., Goldstein, E. D., and Zador, S. (2020). Spatial and temporal dynamics of Pacific capelin Mallotus catervarius in the Gulf of Alaska: implications for ecosystem-based fisheries management. Marine Ecology. Progress Series 637, 117-140. doi: 10.3354/meps13211.

Tsujimoto, M., Kajikawa, Y., and Matsumoto, Y. (2018). A review of the ecosystem concept — Towards coherent ecosystem design. Technological Forecasting & Social Change 136, 49-58. doi: 10.1016/j.techfore.2017.06.032.

Wolfe, Kennedy, Kenyon, Tania M., and Mumby, Peter J. (2021). The biology and ecology of coral rubble and implications for the future of coral reefs. Coral Reefs 40, 1769-1806. doi: 10.1007/s00338-021-02185-9.

Yu, Zicheng, Loisel, J., Brosseau, D.P., Beilman, D.W., and Hunt, S.J. (2010). Global peatland dynamics since the Last Glacial Maximum. Geophysical Research Letters 37, L13402. doi: 10.1029/2010GL043584.